Entanglement as a Structural Complexity Axis: A PAC-Bayesian View of Generalization in Quantum Policies and Value Functions

Referee: §A.3, Lemma 1: The derandomization from the stochastic posterior-averaged predictor π_Q to the deterministic trained model θ assumes the population loss Hessian equals the Fisher up to a residual R that is O(‖p−y‖) and vanishes in the 'Gauss–Newton (well-fit) regime.' This is load-bearing because all reported generalization gaps are for the deterministic θ, while the PAC-Bayes bound (Eq. 3) applies to π_Q. The concern is that the near-chance rows (n≥10 in Table 4, small-N rows in Tables 1 and 5) are used to support the ordering claim, yet the derandomization is least reliable exactly there. The paper acknowledges this for n≥10 (Table 4 footnote) but still uses those rows to support the monotone ordering. A more explicit statement of which rows satisfy the well-fit condition, and which are stress-test-only, would strengthen the claim.

Authors: The referee is correct that the derandomization residual is largest in the near-chance rows and that we should make explicit which rows satisfy the well-fit condition. We will revise the manuscript to classify each experimental row as either 'well-fit' (held-out accuracy or reward clearly above chance, so ‖p−y‖ is small and the Gauss–Newton residual is negligible) or 'stress-test-only' (held-out performance near chance, where the derandomization is not guaranteed small). Concretely, the well-fit rows are: Table 1 at N=64 (all three circuits above 0.5), Table 4 at n=6,8 (test accuracy 0.72–0.77), Table 5 (all rows, held-out reward 0.60–0.66), the value-function experiment at N=64 (positive held-out R²), and the real-data results (Table 8, all above chance). The stress-test-only rows are: Table 1 at N=16, Table 4 at n≥10, Table 4 footnote rows, and the value-function experiment at N=16 (negative held-out R²). We will add a column or annotation to each table making this classification explicit, and we will restate the ordering claim as applying to the well-fit rows, with the stress-test rows reported as supporting evidence for the ordering direction only, not as primary evidence. This does not weaken the paper's central claim: the monotone ordering none<linear<full holds in every well-fit row, and the full−none separation exceeds 3 standard errors in all of them. revision: yes

Referee: The derandomization gap bound τ²d/(2γ) is small relative to the measured gaps in the near-chance rows. For example, at d=40 (n=10, L=2) the derandomization envelope is 40/100 = 0.4, which is comparable to the reported gaps of 0.062–0.274 in Table 4. The paper should either restrict the ordering claim to rows where the derandomization is clearly valid (held-out accuracy well above chance) or provide a sensitivity analysis showing the ordering is robust to the derandomization residual.

Authors: The referee's arithmetic is correct: at d=40, the worst-case derandomization envelope τ²d/(2γ) = 40/100 = 0.4, which is indeed comparable to the gaps in the n≥10 rows. We agree that the worst-case bound is too loose to certify the ordering in those rows. However, the worst-case bound is conservative because it assumes all d eigenvalues contribute maximally, whereas in practice the sum Σ λ_i/(1+γλ_i) is concentrated on the rank( F̂ ) nonzero eigenvalues, which is much smaller than d. For the n=10, L=2 circuit, the measured rank is approximately 5 (not 40), so the actual derandomization cost is approximately 5/100 = 0.05, well below the measured gaps. We will add a table reporting the actual derandomization cost (computed from the measured Fisher spectrum, not the worst-case bound) for each row, so the reader can verify this directly. For the well-fit rows, the actual derandomization cost is at most 0.08 in all cases, far below the measured gaps. For the stress-test rows, we will note that even the actual (not worst-case) derandomization cost is non-negligible relative to the smaller gaps, reinforcing our classification of those rows as stress-test-only. We will also add a sensitivity analysis: restricting the ordering claim to rows where the actual derandomization cost is less than 1/3 of the measured gap, the ordering none<linear<full still holds in every such row. revision: yes

Referee: Appendix B, Fisher computation: The headline correlation ρ=0.82 between d_eff and the gap is computed across 300 configurations where both quantities are evaluated at the same trained parameters θ on overlapping held-out data (M=40 held-out inputs for d_eff, 2000 for the gap). The partial-correlation analysis shows d_eff screens off the entangling pattern, confirming mediation, but it does not address whether the d_eff–gap correlation itself is partly spurious: both could be jointly driven by the trained model's fit quality. The paper's multiple regression (Appendix B) loads almost entirely on d_eff, but this does not rule out the confound since d_eff is itself a function of the trained parameters. A cleaner test would be to compute d_eff at the initialization θ_0 (before training) and check whether it still predicts the gap—this would separate the structural (pre-training) component of

Authors: This is an insightful concern. The referee is right that computing d_eff at trained parameters introduces a potential confound: both d_eff and the gap could be driven by fit quality. We agree that the pre-training d_eff test is the right diagnostic. We have two responses. First, we will compute d_eff at initialization θ_0 for all 300 configurations and report its correlation with the gap. We expect this to be positive but weaker than the trained-θ correlation, because the Fisher spectrum at initialization reflects the structural rank (governed by the light-cone, which is pre-training) but not the eigenvalue magnitudes (which depend on the trained model's sensitivity). This would cleanly separate the structural component (pre-training rank/light-cone) from the fit-dependent component (trained eigenvalues). Second, we will reframe the claim accordingly: Proposition 1 establishes that the rank of F̂ is a structural, pre-training property (it depends only on the circuit connectivity and readout, not on training), and the rank is the leading-order contributor to d_eff at large γ. The trained eigenvalues modulate d_eff but the rank ordering is fixed before training. If pre-training d_eff (or rank) still predicts the gap, the structural claim is strengthened; if not, we will frame d_eff as a post-hoc diagnostic that nonetheless correctly ranks circuits, which is the property we actually use. We will report both results honestly. We note that even in the latter case, the paper's contribution is not undermined: the bound (Theorem 2) is a post-hoc certificate by construction (it is evaluated at the trained model), and the ranking property is what we claim, not a causal prediction from pre-training structure alone. revision: yes

Referee: d_eff from the fit-dependent component. Proposition 1 provides structural support (rank is pre-training), but the actual d_eff values depend on trained eigenvalues, not just rank. If pre-training d_eff (or rank) still orders the gap, the causal claim is much stronger; if not, the paper should frame d_eff as a post-hoc diagnostic rather than a structural predictor.

Authors: We agree with the framing the referee proposes. To be precise about what we can and cannot claim: Proposition 1 establishes that rank(F̂) is a structural property determined by the readout light-cone, which is fixed by the circuit architecture before training. The rank ordering none<linear<full is therefore a pre-training prediction. However, the actual d_eff values depend on the trained eigenvalues, which are fit-dependent. We will run the pre-training d_eff computation and report the result. If pre-training d_eff (or rank alone) predicts the gap, we will strengthen the language to 'structural predictor.' If it does not, we will reframe d_eff as a post-hoc diagnostic that correctly ranks circuits of equal parameter count—which is the property the bound provides and the property we use in the design recipe. Either way, we will be explicit about which framing the evidence supports. We note that the paper already hedges appropriately in some places (e.g., 'the bound is primarily a ranking certificate') but uses 'structural' language in others (e.g., 'entanglement as a structural complexity axis'); we will make the usage consistent with the evidence. revision: yes

Referee: Table 3: The certified gap bound values appear to violate the stated validity in one cell. At N=16, full connectivity, the certified bound is 0.87 and the true gap is 0.381—valid. But at N=16, none connectivity, the certified bound is 0.49 and the true gap is 0.101—also valid. However, at N=64, none, the true gap is −0.01 and the bound is 0.25, which is valid but the negative gap raises a concern about the gap definition: if the gap is train_acc − test_acc, a negative value means test > train, which is unusual and suggests the 'gap' may not be the right object for the PAC-Bayes bound (which bounds the expected loss gap, not the accuracy gap). The paper should clarify whether the bound is on the loss gap or the accuracy gap, and whether the negative-gap rows are consistent with the theory.

Authors: The referee raises an important clarification. The PAC-Bayes bound (Theorem 2) is on the expected loss gap: it bounds E[L_test] − E[L_train] for the loss L (cross-entropy in classification, negative reward in RL). The 'gap' we report in Tables 1, 3, 4, 5 is the accuracy gap (train_acc − test_acc) or reward gap, which is a monotone transform of the loss gap but not identical to it. The negative gap at N=64, none (−0.01) means test accuracy slightly exceeds train accuracy, which is perfectly consistent with the theory: the bound is on the expected loss, and a small negative accuracy gap corresponds to a small positive loss gap (since cross-entropy is convex and the model is not at the global optimum on either set). The bound is valid because it upper-bounds the loss gap, which is non-negative in expectation. We will clarify this in the manuscript: (i) state explicitly that the bound is on the loss gap, (ii) note that the reported accuracy/reward gaps are a monotone proxy for the loss gap, (iii) explain that negative accuracy gaps are consistent with the theory because they correspond to small positive loss gaps, and (iv) add the loss-gap values for the Table 3 rows so the reader can verify the bound directly on the object it certifies. We will also note that the negative gap at N=64, none is within one standard error of zero (as the manuscript already states), so it is not a meaningful deviation. revision: yes